Maternal and child nutrition in the Lives Saved Tool: Results of a recent update

Background The Lives Saved Tool (LiST) is a mathematical modelling tool for estimating the survival, health, and nutritional impacts of scaling intervention coverage in low- and middle-income countries (LMICs). Various nutrition interventions are included in LiST and are regularly (and independently) reviewed and updated as new data emerge. This manuscript describes our latest in-depth review of nutrition evidence, focusing on intervention efficacy, appropriate population-affected fractions, and new interventions for potential inclusion in the LiST model. Methods An external advisory group (EAG) was assembled to review evidence from systematic reviews on intervention-outcome (I-O) pairs for women and children under five years of age. GRADE quality was assigned to each pair based on a LiST-specific checklist to facilitate consistent decisions during the consideration. For existing interventions with new information, the EAG was asked to recommend whether to update the default efficacy values and population-affected fractions. For the new interventions, the EAG decided whether there was sufficient evidence of benefit, and in affirmative cases, information on the efficacy and affected fraction values that could be used. Decisions were based on expert group consensus. Results Overall, the group reviewed 53 nutrition-related I-O pairs, including 25 existing and 28 new ones. Efficacy and population-affected fractions were updated for seven I-O pairs; three pairs were updated for efficacy estimates only, three were updated for population-affected fractions only; and nine new I-O pairs were added to the model, bringing the total of nutrition-related I-O pairs to 34. Included in the new I-O pairs were two new nutrition interventions added to LIST: zinc fortification and neonatal vitamin A supplementation. Conclusions For modelling tools like LiST to be useful, it is crucial to update interventions, efficacy and population-affected fractions as new evidence becomes available. The present updates will enable LiST users to better estimate the potential health, nutrition, and survival benefits of investing in nutrition.

Section One: Quality assignment and application in LiST  Table S1. Quality assignment and application in LiST for intervention-outcome pairs for women of reproductive age or pregnant women  The effect was insignificant when comparing to an active control arm and impact of SQ-LNS only was not available. Very low*: the quality is downgraded to lower than very low LiST-Lives Saved Tool, SQ-LNS-small quantity lipid-based nutrient supplementation, HAZ-height for age zscore, WHZ-weight for height z-score, MD-mean difference, IYCF-infant and young child feeding, SQ-LNS-small quantity lipid nutrient supplementation

Section Two: Description of the meta-analyses reviewed Overview
This section provides a detailed description of systematic reviews and meta-analyses on nutrition interventions. For each intervention, we first list the outcomes reviewed to the right of the intervention. Next, we identify the meta-analysis for the intervention-outcome pair. Then we explain which metaanalysis is more appropriate to be used in LiST based on types of studies included; study settings; definition of intervention/comparison group; study population; and definition of the outcome. Finally, we determine the affected fraction, which is proportion of population who can benefit from the intervention based on study population in the meta-analysis and we also describe the data source for the affected fraction. A box with efficacy or odds ratio and affected fraction applied in the model is attached at the end of each included intervention.
Existing Interventions received by women of reproductive age (WRA) or pregnant women (PW) Balanced energy protein supplementation (BEP)-stillbirth; SGA birth: To determine the affected fraction of the intervention, we checked the characteristics of the participants in the trials. Because the current affected fraction for BEP is women of reproductive age (WRA) with low BMI <18.5(5), we first checked the proportion of low BMI among the study population. In the five trials included, one reported mean BMI in the control=20.7 and intervention=21.3 group (6); one restricted to low BMI<18.5 (4); three studies did not have information on BMI (7-9). Besides BMI, another common recruiting criterion, used by three trials are suboptimal nutrition status (6)(7)(8). Participants included in the trials were not necessarily women with low BMI. If we used low BMI as affected fraction, we might underestimate the impact of BEP. We think food insecurity as a cause for marginal nutrition status better describes the population that can benefit from BEP.
For food insecurity, we previously used the population living below $1.90 a day as a proxy in LiST. At the time, there were no data on prevalence of food insecurity that are available in enough countries for years 2000-2015 or that are the result of regular large-scale collection (5). Now the results of the Food Insecurity Experience Scale (FIES) were available for 77 countries from 2014-2018, reported in threeyear averages (10). FEIS comprises eight questions that reflect self-reported behaviors and experiences associated with increasing difficulties in accessing food due to resource constraints (11). FEIS has three levels 1) food secure or mild food insecurity; 2) moderate food insecurity; 3) severe food insecurity. In LiST, we consider the prevalence of moderate or severe food insecurity as the prevalence of food insecurity. However, FEIS data were missing for several countries, including India and Pakistan which account for roughly 20% of the total LMICs population. To assess whether the percentage of the population living on <$1.90/day could be used for countries where FIES data were unavailable, we performed a correlation analysis in countries where both data were available. We found strong correlation between FIES and percentage of the population living on <$1.90/day (Pearson's correlation coefficient: 0.82), and therefore, use the percentage of the population living on <$1.90/day when FIES data are unavailable. Calcium supplementation-preterm birth; maternal mortality due to hypertensive disorder; preeclampsia: We identified three systematic reviews for calcium supplementation during pregnancy (12)(13)(14). The most recent review by Oh et al excluded studies that collected data before 1995 (14). We think excluding older studies is inappropriate because the impact of calcium supplementation on various health outcomes is through biological pathways that hold true regardless of time. In addition, there were no big fluctuations in the prevalence of low calcium intake in LMICs over the past decade (15 (13). When we looked at the trend of low calcium intake in 10 LMICs with the largest total population, there were small fluctuations over time and low calcium intake was predicted in approximately 70-99% of the population (15). Given the consistent evidence on the association between calcium supplementation and preterm, we decided to use pooled estimates from baseline low calcium intake studies from the Cochrane review to estimate the impact of calcium supplementation on preterm, and only apply the effect to the calcium deficient pregnant women in a country.
We did not identify any newer reviews that reported the impact of calcium supplementation on maternal mortality due to hypertensive disorder. We will keep using the estimates (RR=0.80, 95% CI 0.66, 0.98) from the Cochrane (13). It is noted that only one study was included for the outcome (16). But it is a relatively large study (n=8312) with a baseline low calcium diet population.
We did not currently have pre-eclampsia as a risk factor in LiST. In this round of review, we identified that both the 2018 Cochrane and Oh et al reported impact on pre-eclampsia (13,14). Among the low baseline calcium intake population, the Cochrane found a 63% (RR=0. 36 Oh et al excluded studies that collected data before 1995 and with a smaller number of trials than included in the Cochrane found an insignificant reduction. We do not believe that it is appropriate to exclude older trials in this case. However, given the complex association between calcium supplementation, preeclampsia, and preterm birth, we decided not to add pre-eclampsia as a risk factor in LiST for now. Since the participants in the trials have baseline low calcium intake, the affected fraction in LiST should also be percent of pregnant women with low calcium intake. We previously used the percent of population living under $1.90 a day as proxy due to lack of data availability on calcium intake. Now the country-specific prevalence of inadequate calcium intake has been estimated based on national food balance sheet data, UN population data, multiple food composition tables, and nutrient intake and requirement estimates (15). The data are available for all countries for years between 1961 to 2011. We will use these estimates for the affected fraction benefiting from calcium intake. Iron with or without folic acid supplementation or multiple micronutrient supplementation during pregnancy and anemia-maternal anemia: We identified two systematic reviews on iron supplementation with or without folic acid (14,17). A 2015 Cochrane review found that compared to placebo, iron supplementation with or without folic acid reduced maternal anemia at term by 70% (RR=0.30; 95% CI 0.19-0.46, 14 trials) and iron-deficiency anemia at term by 67% (RR=0.33; 95% CI 0.16-0.69, 5 trials). A more recent systematic review-Oh et al found that compared to placebo, iron supplementation with or without folic acid reduced maternal anemia by 47% (RR=0.53; 95% CI 0.43, 6 trials). Oh et al did not report results for iron-deficiency anemia.
The major difference between two reviews is that Oh et al excluded studies that collected data before 1995 or studies conducted in non-LMICs. Because it is not appropriate to exclude older studies, we decided to use pooled estimates on maternal anemia from 2015 Cochrane review as our reference. We changed the outcome from iron deficiency anemia to all anemia because 1) anemia is a greater and more important public health concern in LMICs 2) there are not good country-specific prevalence trend data for iron-deficiency anemia. It is noted that studies have found no additional benefits on maternal anemia when comparing MMN to IFA (14,18). Therefore, in LiST, we apply the same effect size to MMN and IFA. Since Previous studies (17,19) have also concluded that iron supplementation with or without folic acid does not have any impact on the risk of preterm births, (RR=0.85, 95% CI 0.67-1.08) or SGA (RR=0.93, 95% CI 0.84-1.03).
Previously we applied the impact of IFA to all pregnant women. Majority of the trials in the Cochrane review were conducted in LMICs, therefore we assumed the study population had low iron intake from their usual diet. We changed the affected fraction to percent of pregnant women who are iron deficient. The data for the affected fraction is based on national food balanced sheet (15 We identified three systematic reviews for the intervention (14,18,20 were reported. Both reviews found that MMN have little to no effect on SGA for women with lower BMI. The finding is a bit counterintuitive, but it is possible that for women with lower BMI, MMN is not sufficient to have an effect on SGA without improving energy and protein intake. Given the multiple functions of micronutrients, we still believe that women with lower BMI could benefit from MMN. Therefore we decided to apply the same effect size to all WRA. Since the overall effects were similar in three reviews, we decided to use Oh et al because it is the most recent systematic review.
To be consistent, we also decided to remove the stratification by BMI for the other birth outcomepreterm birth. The same three systematic reviews reported results on preterm (14,18,20 The same three systematic reviews also looked at stillbirth (14,18,20 Iron fortification-maternal anemia: Currently we used a 2019 systematic review on large-scale fortification as our reference (22). We did not identify a newer review for the intervention. In the subgroup analysis, iron fortification reduced anemia prevalence among both non-pregnant women (RR=0.66; 95% CI 0.56-0.76, 9 studies) and pregnant women (RR=0.73; 95% CI 0.64-0.84, 3 studies). We used to apply the same effect size of 34% reduction in iron-deficiency anemia for all WRA. For the similar reason as iron supplementation, we decided to change the outcome to all anemias. And we apply different effect sizes for non-pregnant women and pregnant women to best reflect findings in the review. To our knowledge, no study has examined the combined effect of iron supplementation and fortification. In LiST, the overall effect of the two interventions will be the sum of the two individual effects.
It is noted that the types of studies included in the review varied and there was not too much information on the prevalence of fortification to reach the anemia benefits. Assuming the impact of the iron fortification acts through providing sufficient iron to meet the requirement for women of reproductive age, in LiST we defined the prevalence of iron fortification as percent of women 15-49 years old that receive iron food fortification (18 mg iron per day). The details on the data and method used to estimate the prevalence were published elsewhere (23). Periconceptual folic acid supplementation/fortification-stillbirth due to neural tube defects; neonatal mortality due to neural tube defects; preterm birth; child mortality due to neural tube defects: For periconceptual folic acid fortification and stillbirth, we did not find a more recent review than the one used previously, which included 11 before and after studies and found a 41% (RR=0.59, 95% CI 0.52, 0.68) reduction in neural tube defects (24). The same effect size was applied to intrapartum and antepartum stillbirth due to neural tube defects. Since all the studies were conducted in LMICs, we assumed the study population were in some degree of folate deficiency. Therefore, the affected fraction for the intervention is percent of women reproductive age who are folate insufficient.
We also identified a 2018 meta-analysis of folic acid and risk of preterm birth (25). The review only included observational studies. The intervention was the highest category of folic acid supplementation or dietary folate intake. The comparison was the lowest category of folic acid supplementation or dietary folate intake. Information on exposure of interest was collected via food frequency questionnaires or interviews. The lowest category observed in the included studies ranged from 0 to 200 µg daily, and the highest category ranged from any folic acid or folic acid-containing supplements consumption to ≥1000 µg daily. The outcome-PTB is defined as delivery at <37 weeks gestation.
A total of 14 cohort studies on folic acid supplementation were included for the meta-analysis and they found an inverse association (adjusted OR=0. Of the 8 included studies for preconception folic acid supplementation, 5 were conducted in highincome countries and 3 were conducted in upper-middle income countries. When we checked the adjusted covariates, none of the included studies adjusted for other preconception vitamin use. The largest study included in the meta-analysis, which accounted for about 67% weight, provided folic acid only pills (26). In summary we think there was weak evidence from the review showing an association between increased preconception folate intake and reduced PTB. Since there are few national programs for folic acid supplementation before pregnancy, we decided to also model the impact via periconceptual folic acid fortification.
Since the pooled estimate was reported as OR, we need to convert the OR to RR. We looked at all the individual studies included in the meta-analysis and calculated the weighted preterm birth rate among non-folic acid users. Two out of eight studies did not report the preterm birth rate among the non-folic acid users. One was a study conducted in US (27). Since two other included studies were also conducted in US with a 7% and 9% PTB rate among non-folic acid users (28), we used the average 8% for the US study with missing PTB rate (27). The other study with missing PTB rate was conducted in the Netherlands. Since Netherland is a high-income country, we used a national estimate on spontaneous PTB rate (29). Overall we got a weighted PTB rate of 5% and used it to convert the OR to RR=0.88 (0.85, 0.91). The efficacy of periconceptual folic acid fortification and preterm birth is 0.12 and the affected fraction is percent of population who are folate deficient. The prevalence of folate deficiency is drawn from Beal et al 2017 (15).
No direct data on association between periconceptual folic acid and child mortality due to neural tube defects were available. But evidence has shown that certain proportion of neonates with neural tube defects can survive up to at least 1 year of age (30). To model the potential impact of folic acid fortification on child mortality due to neural tube defects, we need to have data on proportion of child mortality that are attributable to neural tube defects. Unfortunately, such data is not available right now. Therefore, we decided not to include the link between folic acid fortification and child mortality due to neural tube defects now.

Stop smoking education for pregnant women who smoke-preterm birth:
There was evidence showing that stop smoking education might reduce preterm among pregnant women who smoke (32). The review included 17 trials, all conducted in high-income settings. Pregnant women who were current or recent smokers were recruited but the criteria used to classify a 'smoker' varied substantially between trials. The overall pooled estimates find a small but not significant reduction in preterm (RR=0.93; 95% CI 0.77-1.11). The review did find a significant reduction in low birth weight (RR=0.83; 95% CI 0.72-0.94). The significant pooled estimate is probably by reducing small-forgestational-age newborns but the impact on SGA was not reported in the meta-analysis. Since there was no evidence from LMICs and LiST needs an effect on preterm or SGA, we decided not to include the intervention.

Deworming for pregnant women-maternal anemia:
A recent Cochrane review assessed the effect of mass deworming on maternal anemia (33). The study population were pregnant women in second trimester of pregnancy. And the study settings were antenatal clinics covering 6 LMICs. When comparing anthelminthics to placebo or no anthelminthics control, there is little to no reduction in maternal anemia in third trimester (RR=0.85; 95% CI 0.72-1.00, 5 RCTs; low certainty). Most of the trials (n=4) in the review provided IFA tablet to both groups. Because the effect is marginally significant and with low certainty, we decided not to include this intervention in LiST.

Maternal thiamine supplementation-neonatal mortality:
Evidence showing increased breast milk thiamine concentration with supplementation in thiamine deficient populations (34). But there were no direct data for the infant-related outcomes. Due to the insufficient data, we decided not to include this intervention.

Zinc fortification-preterm birth:
Recent meta-analysis found that consumption of zinc fortified food increased plasma/serum zinc concentration, with a corresponding decrease in the prevalence of zinc deficiency (35). Since there were not enough studies on the impact of zinc fortification on outcomes like preterm births, the potential impact could be estimated based on the effect of zinc supplementation.
A recent Cochrane review suggests that zinc supplementation during pregnancy may result in little or no difference in reducing preterm (RR=0.87; 95% CI 0.74-1.03, 21 studies) (36). The analysis did not distinguish between population of low zinc and nutrition and those of normal zinc and nutrition, which is different than the previously published 2015 Cochrane. In the 2015 Cochrane review, the subgroup analysis for women with "low zinc or nutrition" found a treatment effect of RR=0.87 (0.77-0.98)(37). The low zinc or nutrition is defined as women in an area where there is some zinc deficiency, not strictly women who have been determined to be zinc deficient.
Among the five new studies included in the more recent Cochrane, only one specified that the participants had baseline low level of zinc serum. The other four did not provide information on baseline zinc status. But the countries where the four studies were conducted all had a prevalence of low zinc intake greater than 30% (15). Given that supplementation trials showed little to no difference in reducing preterm birth and more research is needed to understand if zinc fortification performed the same way as supplementation, we are not confident to extrapolate the potential impact to zinc fortification.

Omega-3 fatty acid supplementation-preterm births:
We identified a 2018 Cochrane review that looked at omega-3 fatty acid for pregnant women and various perinatal outcomes (38). Only RCTs were included in the review. The review defined the intervention as any forms, types, or dose of omega-3 fatty acid with or without co-interventions. And the control was defined as placebo or no omega 3. All pregnant women were eligible. For studies that provided omega-3 supplements and other agents, the other agents were not always provided for the control group as well. Since some of the studies used a co-intervention like multiple micronutrients which can also reduce risk of PTB, the effect sizes of omega-3 from these studies might be driven by MMS.
In addition, majority of the included studies were conducted in high-income countries (22 out of 26). Causes of PTB are multifactorial, the high-income settings might not reflect the similar multifactorial causes of PTB birth in LMICs. For example maternal infections like malaria and various micronutrient deficiency are also causes of PTB but the prevalence of these risk factors might vary a lot in HICs vs LMICs.
In summary, there is weak evidence showing the potential impact of the omega-3 fatty acid supplementation on PTB, but little of this data is from LMICs. Moreover there is evidence of the adverse impact of omega 3 on prolonged gestation>42 weeks and confidence interval for stillbirth is too wide to rule out harm. Future studies in LMIC must be conducted with extra caution on the potential side effects of the intervention. We recommended not to include this intervention in LiST.
Existing Interventions for infants and children 0-59 months Infant and young child feeding (IYCF) education-early initiation of breastfeeding; exclusive breastfeeding; continued breastfeeding IYCF education can promote early initiation of breastfeeding within 1 hour of birth, exclusive breastfeeding (EBF) for 1-6 months and continued breastfeeding for 6-23 months. In two recent reviews the major difference for the types of studies included is that observational studies were included in Sinha et al but not Lassi et al (39,40). Both reviews provided subgroup analysis by delivery setting: health system and home/community. Sinha  Zinc for treatment of diarrhea-neonatal mortality due to diarrhea; child mortality due to diarrhea: We identified two systematic reviews on the topic (41,42). Walker & Black et al identified high evidence of morbidity reduction based on 2 cluster RCT and >300 hospitalization but low evidence for mortality reduction. The Cochrane review did not report results for diarrhea hospitalizations. Among the four studies included for the meta-analysis on mortality, there were only 3 deaths in zinc group and 8 deaths in placebo group. It is not appropriate to estimate RR of death based on the few deaths.
In LiST, we are comparing children experiencing diarrhea and received zinc vs those who did not. We first assumed that a severe diarrhea incidence would require hospitalization in LMICs. And then we assumed that a severe diarrhea is a proxy for mortality. Therefore we decided to use diarrhea hospitalization to estimate the effect on mortality, using numbers from Walker  Complementary feeding education only-stunting: We identified two systematic reviews that examined complementary feeding education (40,43). Both studies found that complementary feeding education only is only beneficial in a food secure population, but not in a food insecure population. For food insecure population, the suboptimal diet is mainly due to restricted resources therefore education only is not sufficient to improve the diet. Only one study was included in both reviews. In Panjwani et al, food secure is classified primarily based on narrative of baseline population characteristics; secondary approach is to use World Bank national data where upper middle-income is considered food secure. Lassi et al classified level of food security using information in the full texts of the article. In addition, Panjwani et al used WHO growth standard in the meta-analysis. Because Panjwani et al used a clearer definition of food security and WHO growth standard, we decided to keep using Panjwani et al as our reference. We will also update our affected fraction with data from food insecurity experience survey.

Outcome
Odds ratio Affected fraction Reference All three reviews compared one type of complementary food to a control group without any food supplement for children. The pooled estimates on child growth were similar across three reviews.
We wanted to isolate the effect of non-LNS complementary food, but to our knowledge, there is no review focused on non-LNS only. Therefore we conducted a de novo meta-analysis based on the studies included in Panjwani et al and Lassi et al. Within the non-LNS category, we broke it further down to local food and prepared non-LNS food. Local food is defined as food mixture without fortification using locally available ingredients or other un-mixed local food, regardless of caloric content. Prepared non-LNS is defined as food-based matrix that is not LNS with fortified multiple micronutrients. It was noted that all prepared non-LNS contains more than ~125 kcal. We excluded the intervention arms that provided medium-quantity-LNS (45,46). Two studies included in Lassi et al is not appropriate. One study did not provide any types of complementary food (47). One study provided other food supplement for children in the control group (48).
By pooling the effect size for the subcategories of complementary food we want to 1) determine if SQ-LNS is more effective than other types of complementary food in improving growth outcomes 2) check if local food without any fortification can improve growth outcomes. We decided to use absolute mean difference (MD) between intervention and control groups in change in height-for-age z-score (HAZ) and weight-for-height z-score (WHZ) from baseline to end line as our effect size. Because all three reviews reported these outcomes, and more studies were included for the outcomes. Since Panjwani et al applied stricter criteria where studies with high attrition rate or insufficient sample size were excluded, we conducted two sets of meta-analysis-one with stricter inclusion criteria and one with looser inclusion criteria.
Two studies were excluded under the stricter criteria, but since the two studies were relatively small, the exclusion did not impact the overall pooled estimates, see section four (49,50). In random-effects model The results were generally similar in random-effects model and fixed effects model. The only significant difference is the subgroup analysis for local food. In the fixed effects model, local food reduced WHZ (MD=0.33; 0.12-0.55) and HAZ (0.50; 0.29-0.71). Given the high heterogeneity among studies on local food, we think random-effects model is more appropriate.
Without searching for other studies of prepare non-LNS or local food, we decided to rename the intervention "Provision of appropriate fortified complementary food". The definition of the intervention is providing fortified and nutritious food. And we will make a note that the effect size is based on SQ-LNS trials. We used the same method described in Panjwani et al to convert MD to OR (43). The affected fraction for the intervention is percent of population who are food insecure. And the prevalence data are from the food insecurity experience scale and poverty headcount ratio at $1.9 a day.
A recent meta-analysis also looked at SQ-LNS and child mortality (51). The paper included RCTs, comparing small-and medium-quantity LNS with non-LNS controls. Small-and medium-quantity LNS was defined as <500 kcal/day. The non-LNS arm did not receive any other types of child supplementation, such as multiple micronutrient powder or other fortified blended food. The review also excluded trials with maternal LNS supplementation or trials focused primarily on treatment of malnutrition. The outcome is all cause child mortality after 6 months. The risk of mortality was lower in the LNS arms than in the non-LNS control arms (RR=0.73, 95% CI 0.59-0.89, 13 studies). But when comparing multicomponent arms with LNS groups and comparison groups that contained all the same components except LNS, the effect estimate was attenuated (RR=0.82, 95% CI 0.61-1.10, 15 studies).
Most of the studies (n=12) provided SQ-LNS. Given that 1) comparing to active control arm, the effect was attenuated; 2) the study did not report cause-specific mortality; 3) there was no subgroup analysis for SQ-LNS only, we decided to not add the link between provision of complementary food and child mortality.
We identified a IPD meta-analysis on SQ-LNS and child anemia (52). Only RCTs conducted in LMICs are included in the meta-analysis. The intervention group received SQ-LNS with or without a cointervention. The control group received placebo or an intervention without any types of LNS or other child supplement. Child anemia is defined as Hb<110 g/L. All the trials included in the review were conducted among children 6-24 months. SQ-LNS increased hemoglobin concentration (MD=2.77 g/L; 95% CI 2.31, 3.23 g/L) and reduced the prevalence of anemia (PR=0.84, 95% CI 0.81-0.87, 14 trials). Since SQ-LNS contains certain amount of iron, it is logical to see a reduction in child anemia.
However, it is complex to include child anemia into the LiST model. Child anemia determined by hemoglobin level should be interpreted as a distribution, meaning that an intervention can improve hemoglobin level but if an individual has a very low baseline hemoglobin level, the improvement might not be sufficient to make the individual non-anemic. To include child anemia as a risk factor in LiST, we need to have some baseline information on the hemoglobin distribution among children in different countries. But such detailed country-level data was not available right now. Another concern is that LiST is a mortality-focused model, meaning all the risk factors are linked to mortality or another risk factor. However, currently we do not have evidence on the connection between child anemia and mortality. Therefore, we decided that we will not include the impact of SQ-LNS on child anemia in the model until further data and evidence on child anemia become available. We identified three meta-analyses for vitamin A supplementation and child mortality due to diarrhea (53,54,58). The 2011 Cochrane review and Black et al included the same set of trials. But in Black et al, with the assumption that all the effects were in the subset of the trial participants with low serum retinol, the adjusted RR was calculated. The newer Cochrane review added the DEVTA trial published in 2013, where it found little to no impact on child mortality due to diarrhea (59). DEVTA trial has received various criticisms since publication (60)(61)(62). We decided to keep using adjusted RR from Black et al and apply to the present prevalence of vitamin A deficient children.
The affected fraction for the intervention is percent of children who are vitamin A deficient. We used country-specific prevalence of inadequate vitamin A intake as proxy for prevalence of vitamin A deficiency. Data are available for all countries included in LiST for years between 1961 to 2011 (15). The data were estimated based on national food balance sheet data, UN population data, multiple food composition tables, and nutrients intake and requirements data. We were aware that other studies have also reported prevalence of low serum retinol in LMICs (63). But the data were not available for time trends. Zinc supplementation-diarrhea incidence; pneumonia incidence; child mortality due to diarrhea; child mortality due to pneumonia; stunting: We identified three reviews on zinc supplementation for children and disease incidence-diarrhea and pneumonia (53,55,64). The RR for diarrhea incidence and pneumonia incidence were consistent across three reviews. The same assumption adjustment for vitamin A supplementation were also applied for zinc supplementation (53). Since we want to account for time varying zinc-deficiency, we decided to use Black et al as our reference.
Two reviews looked at zinc supplementation and cause-specific child mortality-mortality due to diarrhea and mortality due to pneumonia (53,64). Three studies were included in both reviews. Therefore, the pooled estimates were consistent within the two reviews. Black et al also reported adjusted RR that attributed the overall effect to the zinc deficient fraction. Another older review found significant impact on all-cause mortality among children 12-59 months (65). Since the impact for allcause mortality is significant and there are significant effects on diarrhea and pneumonia incidence, there is increased plausibility of the mortality effects. We decided to include the impact.
We identified two reviews on zinc supplementation and stunting (55,66 The Cochrane review found that zinc supplementation has negative impact on linear growth in children 6-12 months (SMD=-0.26; 95% CI -0.33, -0.19)(67). There were three new studies included in the more recent systematic review, but their study population also included 6-12 months infants. We think that different age range inclusion explained the insignificant findings in Tam et al. Since we have the estimate for prevalence of zinc deficiency among children 1-4 years, we will keep the impact of zinc supplementation on stunting and use the pooled estimates from Bhutta et al.
The affected fraction for the intervention is percent of children 1-4 years who are zinc deficient.
Currently we use prevalence of low zinc intake as a proxy to estimate the prevalence of zinc deficiency (68). But evidence has shown that this value may underestimate the prevalence of zinc deficiency as measured by plasma or serum zinc concentration (69). But the prevalence of zinc deficiency based on plasma/serum zinc is only available for 19 countries. When comparing percentage of low plasma/serum zinc with low zinc intake, the results were not consistent, so it is hard to apply a formula for adjustment. More work is need for the better data on prevalence of zinc deficiency. Systematic reviews of deworming were often conducted for children under 16. A 2017 literature review identified randomized and quasi-randomized trials for meta-analysis on outcomes assessed in populations that primarily contained children younger than 5 years (70). They identified two systematic reviews and then conducted a meta-analysis using appropriate trials included in the two reviews. Two new meta-analyses based on studies for children younger than 5 years did not find significant effect of deworming on weight- Taylor Vitamin D for children 1-59 months-pneumonia incidence; stunting: We identified an IPD meta-analysis of 25 RCTs on vitamin D and respiratory infection (73 Given the evidence from two systematic reviews, we decided not to include the intervention.
Prophylactic antibiotics for children 1-59 months-stunting: To our knowledge, there were no systematic review conducted for the intervention. Due to the insufficient data, we will not include this intervention.
Nutrition sensitive agriculture intervention-appropriate complementary feeding: We did not identify any studies that looked at the direct impact of nutrition sensitive interventions and growth outcomes. A recently published meta-analysis found potential impact on diet diversity score and minimum diet diversity in children 6-59 months (75). However, the definition of nutrition sensitive intervention is not clear, and the actual interventions varied a lot across studies. Since the standard of the intervention is vague and the impact pathway is more complex than fixing micronutrient status, we decided that it is not appropriate to include the intervention in LiST.
Zinc fortification-diarrhea incidence; pneumonia incidence; child mortality due to diarrhea; child mortality due to pneumonia; stunting: Recent meta-analysis found that consumption of zinc fortified food increased plasma/serum zinc concentration, with a corresponding decrease in the prevalence of zinc deficiency (35). Since there were not enough studies on the impact of zinc fortification on outcomes like diarrhea incidence, pneumonia incidence, and stunting, the potential impact could be estimated based on the effect of zinc supplementation.
We extrapolated the estimates of effect size based on zinc supplementation trials to zinc fortification (53,66 Iron fortification-child anemia: We identified a systematic review on iron fortification and child anemia (22). Both observational studies that evaluate national/subnational fortification program and large scale (n>1000 per arm) randomized or quasi-randomized controlled trials were included in the review. All the included studies were conducted in LMICs settings. The fortification standard in the intervention group ranged from 2.2 mg/100g to 29.6 mg/100g. The control group was either a non-fortified group or a pre-fortification population. The review looked at children less than 7 years old. Iron fortification was found to reduce anemia (RR=0.61; 95% CI 0.38-0.96, 7 studies). The intervention might also improve hemoglobin concentration (SMD=0.30; 95% CI -0.05, 0.66, 6 studies). Since iron fortification is likely to increase children's iron intake, it is logical to observe potential improvement in hemoglobin concentration and anemia. But there are lack of connection between child anemia and mortality and lack of data availability on hemoglobin distribution among children. Therefore we decided not to add the link between iron fortification and child anemia in LiST until further data and evidence on child anemia become available.
Multiple micronutrient powder for children-child anemia: We identified two Cochrane reviews for multiple micronutrient powder (76,77). Both reviews only included RCTs. The intervention was addition of powders containing vitamins and minerals (at least iron, zinc, and vitamin A) to semi-solid food immediately before consumption. The intervention is also known as point of use fortification. The control was placebo or an intervention without iron-containing supplements. The target population in the two reviews were different: one for children ages 6 to 23 months and the other for children 2-12 years with subgroup analysis for 2-5 years. Neonatal vitamin A supplementation-neonatal mortality due to diarrhea; child mortality due to diarrhea: We identified a 2019 IPD analysis on neonatal vitamin A supplementation and infant mortality (78). Only RCTs were included in the review. The intervention was defined as 25,000-50,000 IU vitamin A given within the first 2-3 days of life. And the control group received placebo. The review looked at mortality from data of supplementation to 6 months and to 12 months. All 11 RCTs included in the review were conducted in Asia or Africa.
The reduction in mortality <6 month was not significant in the overall pooled estimates (RR=0.97, 95% CI 0.89-1.06). But in the subgroup analysis, the reduction in mortality <6 months was significant in studies with moderate/severe maternal vitamin A deficiency, defined as greater or equal to 10% (RR=0.87, 95% CI 0.80-0.94, 3 trials). The reduction in mortality <6 months was also significant in studies conducted in Asia (RR=0.87, 95% CI 0.77-0.98, 5 trials). The three trials with moderate/severe maternal vitamin A deficiency were also conducted in Asia.
The review also found that compared to placebo, neonatal vitamin A supplementation did not reduce mortality <12 months (RR=1.00, 95% CI 0.93-1.08, 10 trials). None of the subgroup analysis found a significant impact.
Given the sufficient evidence from the literature, we think it is important to include this intervention. In LiST, we only have cause-specific mortality. The most appropriate cause-specific mortality for neonatal vitamin A supplementation is mortality due to diarrhea for children <6 months. It is noted that the review found 13% reduction on all-cause mortality, our approach might underestimate the actual efficacy of neonatal vitamin A supplementation on mortality due to diarrhea. We define the interventions as percent of neonates receiving 25,000-50,000 IU vitamin A within the first 2-3 days of life. The efficacy is 0.13 and the affected fraction is percent of pregnant women who are vitamin A deficient.
We acknowledge that there are limited data available for percent of pregnant women who are vitamin A deficient. We choose to use prevalence of VAD in pregnant women from the 2009 WHO report. Alternative options that we discussed were using prevalence of night blindness as a proxy or only applying the effect to certain countries with high VAD. Using country as affected fraction is not a common practice in LiST model and we think we are not ready to add this type of affected fraction. Prevalence of night blindness could be a possible proxy as it is one of the symptoms for vitamin A deficiency, however by checking for the country-level prevalence, there were also limited data available for the indicator. Given that the intervention is effective at reducing mortality in settings with high prevalence of VAD, we recommend the use of prevalence of VAD in pregnant women.
We also think this is some good evidence to advocate for vitamin A fortification for mother to improve maternal vitamin A status. Neonatal zinc supplementation-neonatal mortality due to sepsis: We identified a systematic review on zinc for prevention and treatment of sepsis (79). Only RCTs were included in the review. The intervention was oral zinc supplementation in any form and dose with or without other micro-/macronutrient or antibiotics that the control group also received. The control was placebo or a no-zinc intervention. The target population in the review were young infants less than 4 months. There was no restriction on birth weight, gestational ages, and underlying co-morbidities for the included population.
Preventive zinc supplementation for preterm neonates who are at higher risk for sepsis reduced mortality (RR=0.28, 95% CI 0.12-0.67, 2 studies, 265 participants). Evidence from two studies is not sufficient to prove the benefit impact of preventative zinc and mortality among preterm infants. We decided not to add the link between preventive zinc supplementation for preterm neonates and mortality. But given the potential benefits, we think this is an area where more research is needed to better understand the risk association.
For zinc supplementation as a therapeutic intervention for infants with sepsis, the intervention did not reduce all-cause mortality (RR=0.66, 0.40-1.08; 5 studies). In the subgroup analysis by dosage, only dose of 3mg/kg/twice a day was found to be effective at reducing mortality (RR=0.49, 95% CI 0.27-0.87, 2 studies, 359 participants). Evidence from two studies is not sufficient to prove the benefit impact of zinc for treatment of sepsis and mortality. But given the potential benefits, we think this is an area where more research is needed to better understand the risk association.